Experimental design is how a scientist plans a fair comparison before collecting data. It establishes which units receive different conditions, which outcomes matter, what must be measured and how alternative explanations will be checked. Good design makes the final answer meaningful; statistical sophistication cannot compensate for a fundamentally confused comparison.
This guide explains controls, randomisation, blocking, factorial interactions, replication, clusters, missing outcomes and ethical constraints through original worked calculations and changed-context exercises. The goal is practical reasoning that can travel from a school experiment to research and industry without copying methods whose assumptions do not apply.
Choose a question-first reading route
From question to fair comparison · Chapters 1–7. Start →
Blocking, factorials and independent units · Chapters 8–14. Start →
Clusters, contamination, measurement and analysis · Chapters 15–21. Start →
Ethics, calculations and learning · Chapters 22–27. Start →
Full chapter index · Worked design workshop · Specialist eduKate articles · Gold Standard master
Chapter index
From question to fair comparison
- 1. Experimental design begins before the first measurement
- 2. How experimental design differs from scientific method
- 3. Define the question, population and outcome
- 4. The experimental unit is not always the observation
- 5. A fair comparison needs a meaningful control
- 6. Random assignment addresses selection bias
- 7. Allocation concealment is different from blinding
Blocking, factorials and independent units
- 8. Blocking controls known nuisance differences
- 9. Paired and repeated-measures designs
- 10. Factorial experiments ask about interactions
- 11. Two-level designs and the cost of complexity
- 12. Main effects do not tell the whole story
- 13. Replication means independent experimental information
- 14. Sample size, power and detectable effects
Clusters, contamination, measurement and analysis
- 15. Clusters require cluster-aware analysis
- 16. Contamination, interference and treatment spillover
- 17. Crossovers and the problem of carryover
- 18. Measurement quality is part of causal identification
- 19. Missing data, dropouts and selective observation
- 20. Confounding, bias and alternative explanations
- 21. Choose analysis before seeing the favourable chart
Ethics, calculations and learning
- 22. Sequential experiments and stopping decisions
- 23. Safety and consent before intervention
- 24. Worked factorial: interaction is a real result
- 25. Worked blocking: separate shift effects from treatment
- 26. Worked 2-to-the-3 factorial run count
- 27. Frequently asked questions and practical route
The design decisions that precede an analysis
| Decision | Question to answer | Risk if ignored |
|---|---|---|
| Comparison | What alternative is meaningful? | Confounding treatment with conditions |
| Assignment | Which independent units receive conditions? | Pseudoreplication and selection bias |
| Measurement | Which prespecified outcome, unit and time? | Changing target after seeing results |
| Analysis | Which effects, interactions and uncertainties? | Misleading significance or collapsed interactions |
| Ethics | What approvals and protections apply? | Unjustified or unlawful intervention |
1. Experimental design begins before the first measurement
Experimental design is the discipline of deciding how an investigation will compare conditions so that its results can answer a causal or process question. It includes choosing an outcome, defining interventions and controls, assigning units, managing confounders, planning repeated measurements and deciding how results will be analysed. It happens before an experiment is run, not after the data reveal an attractive pattern.
A good design is not necessarily complicated. Sometimes one controlled comparison supplies a defensible answer; sometimes interactions, clusters or time trends demand a more involved strategy. The central question is what comparison would make us change our belief about the proposed cause, and which competing explanations that comparison can reasonably eliminate.
2. How experimental design differs from scientific method
The scientific method is a broad family of practices including observation, modelling, inference and criticism. Experimental design concerns how evidence from planned interventions is created. It is more specific than deciding to change one variable: it asks whether the assignment, comparison, timing and measurement jointly identify what caused an observed difference.
Read Scientific Method for the broader account of evidence, and Statistics for data analysis. This guide owns the design choices that make later analysis meaningful. Sophisticated statistics cannot recover a causal comparison that the experiment never established.
3. Define the question, population and outcome
Start by describing the target population or system, intervention, comparison and outcome. In an educational trial, the question might concern independently solved unfamiliar algebra problems after four weeks, not whether students enjoyed a lesson. In a manufacturing study, the outcome might be defect proportion rather than merely the speed of the production line.
Operational definitions should be fixed before allocation. Write how each outcome is observed, in which units, and at what time. Distinguish primary from secondary outcomes. If an outcome can be quietly changed after results are inspected, the reported study may answer a question selected for its favourable result instead of the original research question.
4. The experimental unit is not always the observation
The experimental unit is the smallest unit independently assigned to a condition. Researchers may record many measurements from one person, plant, school or machine, but repeated observations do not create the same number of independently assigned units. Confusing these numbers produces pseudoreplication.
Suppose four classrooms receive a teaching strategy, and each contains thirty pupils. The treatment was allocated to classrooms, not to 120 independent pupils. The comparison must account for variation between classrooms. Measuring every pupil is valuable, but their outcomes can be correlated through shared teachers and settings.
5. A fair comparison needs a meaningful control
A control condition supplies a reference for what might have happened without the intervention. It could be usual practice, a different treatment or a no-treatment condition where ethical and practical. The right comparator depends on the research question; an artificial placebo or inactive condition is not automatically appropriate.
If an intervention is evaluated against a deliberately ineffective comparator, the practical conclusion may still be weak. Ask what decision-makers could realistically choose instead. Ensure measurement, follow-up and outcome definitions are comparable across groups, or differences in the research procedure may create apparent treatment effects.
6. Random assignment addresses selection bias
Randomisation assigns units to conditions by a chance-based procedure rather than a preference linked to prognosis or performance. Its aim is to make treatment assignment independent of potential outcomes under an appropriate design. It supports valid comparisons over repeated assignments, but a single small random allocation can still produce chance imbalances.
Document the sequence-generating method, eligible units, allocation ratio and any restrictions. Merely assigning a few volunteers alternately is not randomisation and may be predictable. Statistical analysis should match the allocation scheme, and results must still be interpreted with uncertainty.
7. Allocation concealment is different from blinding
Allocation concealment prevents people recruiting participants from knowing a forthcoming assignment before enrolment is fixed. Blinding or masking prevents specified participants or investigators from knowing assigned conditions during intervention or outcome assessment. They guard against different biases and should not be presented as synonyms.
In human research, it may be impossible to conceal a visible treatment from its recipient, yet a separate assessor can sometimes remain unaware of allocation. State who was masked and how. A label like ‘double-blind’ without identifying which parties knew what is less informative than a clear description of the actual safeguards.
8. Blocking controls known nuisance differences
A nuisance variable is a factor likely to influence the outcome but not the central causal question. Blocks organise comparisons among units that share such conditions, such as production batches, days, classrooms or instrument sessions. Randomisation within blocks can then make comparisons less vulnerable to large predictable differences.
For example, test a new process at both morning and evening shifts rather than assigning all treatment runs to the morning shift. Blocking is not equivalent to making every influence disappear. The block structure and its limitations belong in analysis, especially if some treatment combinations cannot be observed within the blocks.
9. Paired and repeated-measures designs
Repeatedly measuring the same participant or specimen can increase precision when within-unit differences are informative. A paired design might compare matched objects or before-and-after outcomes. But the design must consider order, maturation, practice and carryover effects.
A pre–post change does not by itself establish causation: other changes may occur during the interval. A matched control or randomised crossover may support stronger inference under appropriate assumptions. State why pairing is scientifically relevant and whether the analysis correctly preserves it.
10. Factorial experiments ask about interactions
A factorial design combines levels of two or more factors so researchers can estimate their individual effects and whether the effect of one factor depends on another. A two-by-two design compares four combinations, not simply two treatments. A scientifically important interaction may be invisible when researchers vary only one factor at a time.
Suppose an adhesive responds differently to curing temperature depending on humidity. Testing each factor independently may miss a combination that causes failure. Factorial designs help find these dependencies efficiently, but their interpretation requires clear factor coding, sufficient replication and appropriate model assumptions.
11. Two-level designs and the cost of complexity
With k factors each tested at two levels, a full factorial contains 2^k distinct combinations. Three such factors give eight combinations before adding replicates, blocks or centre points. As the number of factors grows, the required runs increase quickly.
Fractional factorial designs can reduce cost for early screening but deliberately confound some effects. Researchers must understand which interactions are indistinguishable under the chosen fraction. The NIST Engineering Statistics Handbook documents these trade-offs. Saving runs is sensible only when the lost ability to distinguish effects is acceptable for the research purpose.
12. Main effects do not tell the whole story
A main effect summarises the average change associated with a factor across the selected levels of other factors. An interaction means that the effect depends on the other factor. Averaging over a strong interaction can conceal that one treatment helps under one condition but harms under another.
Before reporting an overall effect, inspect treatment combinations and ask which population or operating ranges are relevant. If the design represents only narrow factor levels, the result does not automatically apply outside them. The interaction is a scientific explanation opportunity, not an inconvenient statistical complication.
13. Replication means independent experimental information
Replication repeats an experiment on independently assigned units under the defined design. Repeating the readout on one treated sample may improve measurement precision but does not replicate the treatment on an independent experimental unit. Distinguish technical replicates from biological or operational replicates.
A study with hundreds of instrument readings from one specimen may contain little information about variability across specimens. State the numbers of independent units, repeated measurements and experimental sessions separately. Use the structure to calculate uncertainty rather than treating every row as an independent trial.
14. Sample size, power and detectable effects
Planning sample size requires a meaningful target effect, plausible outcome variability, an allocation scheme, error criteria and the intended analysis. A small experiment may be useful for checking feasibility or calibrating a method, but may provide inconclusive evidence about a small effect.
Power calculations inherit assumptions. If the expected variability or treatment effect is unrealistic, the resulting sample size may be inappropriate. A non-significant result in an underpowered study is not proof of no effect. Report uncertainty and the range of effects the study can reasonably rule out.
15. Clusters require cluster-aware analysis
When schools, clinics, teams or work sites are assigned as groups, members of a group may be more similar than members from different groups. Intraclass correlation reduces independent information compared with the same number of individually randomised participants. The NIH Research Methods Resources explain why clustering must be incorporated into design and analysis.
A common mistake is to randomise one school to each treatment and then analyse hundreds of students as if their individual observations created hundreds of independent treatment assignments. The intervention is confounded with the two schools; the student count cannot repair that design. More independent clusters are often essential.
16. Contamination, interference and treatment spillover
Experiments frequently assume one participant’s assigned condition does not change another participant’s outcome. In classrooms, workplaces or networks, participants may share strategies or resources across trial arms. This interference complicates the interpretation of a simple individual-treatment effect.
Plan for foreseeable sharing rather than merely telling participants not to speak. Cluster assignment may reduce spillover in some contexts, but introduces intraclass correlation and other design challenges. Describe the possible contamination routes and whether the intended estimate represents an individual effect or an effect under realistic group implementation.
17. Crossovers and the problem of carryover
In a crossover design, each unit receives different conditions in a planned sequence. This can reduce between-unit variability, but treatment order and residual effects can bias comparisons. A washout period may be needed when scientifically justified, and some interventions cannot be meaningfully undone.
A student who learns a problem-solving strategy may retain it after switching back to an old teaching method. A crossover study cannot simply assume learning disappears. Choose another design if the effect is persistent. The question of reversibility must be answered before scheduling treatment periods.
18. Measurement quality is part of causal identification
Even perfect allocation cannot save an experiment whose outcomes are measured inconsistently. If assessors spend longer observing the treated group, or if an instrument changes calibration between conditions, a measurement difference can masquerade as an intervention effect.
Blind outcome assessment where possible, use the same instruments and scoring procedures, and record changes in setup. For physical experiments, check range, uncertainty and drift using the Scientific Instrumentation guide. The best trial result begins with a trustworthy measurement chain.
19. Missing data, dropouts and selective observation
Participants may miss follow-up, instruments can fail and specimens may be unusable. If missingness is related to the outcome or treatment, simply analysing complete observations may bias the estimate. Missing data should be anticipated in recruitment, data collection and statistical analysis planning.
Report the number assigned, the number measured and the reasons data are missing. A group showing 80% success among survivors of follow-up may not be comparable with another group that retained almost all participants. Describe assumptions used to handle missing values rather than quietly erasing inconvenient rows.
20. Confounding, bias and alternative explanations
Confounding arises when another variable is related both to the treatment or exposure and to the outcome. Randomisation can protect against many such biases in expectation, while observational designs require other identification strategies. Bias may also enter through selection, measurement or deviations from the intended intervention.
Keep a causal story with candidate pathways and alternative explanations. Adjusting for every measured variable is not always wise: conditioning on the wrong variable can create new bias. Ask which variables existed before treatment and which are consequences of the intervention. A design diagram can be more helpful than a very long regression formula.
21. Choose analysis before seeing the favourable chart
Prespecification clarifies which outcome, comparison, model and decision rule were planned. Exploratory discovery is valuable when labelled honestly; presenting a newly discovered pattern as the original confirmatory hypothesis creates false confidence.
Distinguish an estimated treatment effect, its uncertainty and the threshold for a practical decision. A small p-value alone does not measure importance or prove all assumptions. Report effect sizes, intervals and sensitivity to reasonable alternatives. When many tests are explored, explain the multiple-comparison issue.
22. Sequential experiments and stopping decisions
Some studies examine data at planned interim points for safety, futility or other reasons. Repeatedly checking ordinary significance thresholds without a suitable sequential design can alter false-positive error behaviour. Timing and stopping rules should be part of the statistical plan.
Clinical research has additional ethical and regulatory requirements. Some early stopping decisions protect participants, but cannot be inferred from one generic statistical rule. Use competent oversight, predefined procedures and appropriate expert analysis; a school project should not copy high-stakes clinical procedures without context.
23. Safety and consent before intervention
Research design includes asking whether the experiment is permissible. Studies involving children, patients, sensitive records, animals or hazardous materials can require consent, ethical review and safety controls. A more statistically powerful intervention is not justified if it exposes participants to unacceptable harm.
A harmless classroom demonstration and a medical trial demand different safeguards. Identify vulnerable populations, privacy concerns and the authority responsible for approvals. Follow the Research Ethics root for the wider principles. Never interpret a worked example as approval to perform a regulated intervention.
24. Worked factorial: interaction is a real result
Invented two-factor experiment: baseline factor A=low, B=low gives result 10. A=high, B=low gives 14; A=low, B=high gives 12; both high gives 22. Raising A at low B changes the result by 4, but raising A at high B changes it by 10. The difference of these effects is an interaction contrast of 6.
The average main effect of A across B levels is [(14+22)/2] − [(10+12)/2] = 7. This summary does not mean the actual effect is 7 in either observed condition. Report the four combinations and the interaction, then consider replication, variability and whether either factor’s level is relevant to real operations.
25. Worked blocking: separate shift effects from treatment
Invented experiment across two shifts: during morning, the untreated result is 10 and treated result is 13. During evening, the untreated result is 18 and treated result is 21. Each within-shift treatment contrast is 3, while the evening baseline is 8 higher than morning.
Comparing only morning untreated with evening treated gives an apparent difference of 11, but that confounds treatment with shift. Randomising conditions within shifts and analysing the blocks protects the main comparison. The numbers illustrate a contrast; they provide no uncertainty estimate or real treatment claim without replication.
26. Worked 2-to-the-3 factorial run count
An experiment has three binary factors: low or high temperature, low or high pressure, and short or long processing time. A full factorial design requires 2×2×2=8 unique factor combinations. If each combination is repeated on three independent batches, the total is 24 experimental runs.
Taking three sensor readings of the same batch instead is not identical to having three independently run batches. The planning document should distinguish measurement replicates from the units independently exposed to each combination. Cost estimates and uncertainty calculations depend on that distinction.
27. Frequently asked questions and practical route
Is random allocation a guarantee that the groups are identical? No. Does blinding mean the same thing as allocation concealment? No. Is a before-and-after change proof of a treatment effect? No. Can a very large pupil count repair a trial with only one school per arm? No. Is a significant main effect enough when a strong interaction exists? Often not.
Beginners can design fair object tests and identify measurement units. Intermediate learners can randomise and block simple conditions, calculate treatment contrasts and practise changed-context checks. Advanced researchers should work with appropriate design and statistical specialists for factorial, repeated-measures, cluster and ethically regulated trials.
Fourteen original experimental-design cases
1. The two-sunlight plant growth trap
An invented class places one plant under a brighter lamp and another under a dimmer lamp, then concludes that light alone caused different growth. The plants may differ in species, soil, water, health or pot size. More precise rulers cannot resolve confounding if all other factors changed together.
Design a fairer investigation using multiple comparable plants assigned to conditions, consistent care, an appropriate light measure and predetermined outcomes. Record ethical and safety limits, and do not claim one classroom demonstration establishes a universal growth law.
2. Random assignment versus alternate order
Suppose a researcher assigns every odd-numbered arriving volunteer to treatment and every even-numbered one to control. The method is systematic and may be predictable, but is not the same as concealed random allocation. A recruiter who knows the next assignment could influence who enrols.
Demonstrate a genuinely chance-based procedure appropriate to the project, document how assignments are protected and compare baseline characteristics. Randomisation is not an aesthetic label: its function is to reduce allocation-linked bias under a defensible method.
3. A trial with a hidden subject-line change
One email campaign tests two message bodies but also changes the subject line only in the treatment arm. If response rates differ, the body content and subject line are confounded. The result cannot cleanly attribute the difference to either one.
Keep the subject line identical while testing the body, or deliberately use a factorial design that tests both factors and their interaction. State which outcome was specified in advance, such as clicks or completed applications, and avoid calling mere message openings proof of comprehension.
4. A matched pair study and its boundary
An invented materials test pairs two parts from the same production batch, randomly assigning one to a new treatment and the other to usual process. Pairing helps control batch differences, and the appropriate comparison is the within-pair difference.
Ask whether the parts are truly comparable and whether treatment could affect its paired control through shared heat or equipment. Do not analyse paired observations as unrelated groups without considering the design. Report how pairs were formed and which variation pairing was meant to remove.
5. The factorial interaction that averaging conceals
Use the four invented results 10, 14, 12 and 22 from the worked factorial. The apparent benefit of raising factor A is 4 when B is low but 10 when B is high. A single headline stating that A improves output by 7 erases that dependence.
Plot the two effects by B condition using a clear common vertical axis. Discuss whether the 6-unit interaction could be practically important and what independent replication would be needed. This trains readers to inspect combinations before interpreting a marginal summary.
6. The school intervention with one classroom per arm
One classroom receives a new reading strategy while another uses existing lessons. Even if each class has thirty pupils, assignment was at the classroom level, leaving only two independently assigned clusters. Teacher style, timetable or class composition may be indistinguishable from the intervention.
Explain why treating sixty student outcomes as sixty independently randomised units is invalid. A stronger design would involve more classrooms and appropriate cluster-aware planning, subject to ethical and administrative approval. The number of independent assignment units matters.
7. A pre–post comparison with normal maturation
An invented group of students improves from 12 correct answers to 17 after six weeks. The increase is five, but it may reflect normal practice, a changing test, other lessons or the targeted intervention. A gain by itself does not isolate the reason.
Plan a suitable comparison group, use equivalent assessments and record other relevant teaching. Define the target effect and time horizon. The arithmetic describes observed improvement; causation requires a credible research design.
8. A simple difference-in-differences calculation
Invented observational data: a programme group rises from 60 to 70 while a comparison group rises from 65 to 69. Gains are 10 and 4 respectively, so the difference in differences is 10−4=6 points. The calculation adjusts for the observed common period comparison under its model.
It is not automatically causal. A key requirement is a defensible parallel-trends assumption absent treatment, along with other design considerations. Compare earlier trends, intervention timing and concurrent changes before attributing six points to the programme.
9. Contamination in a lesson trial
Students assigned to different revision methods attend the same after-school group and exchange materials. The methods are no longer isolated as intended; the measured contrast can become smaller or otherwise distorted through spillover.
Document likely routes of sharing, select a feasible unit of allocation and decide whether the real-world policy question includes such interaction. Do not blame pupils for collaborating; design a study that reflects or accounts for how the setting actually works.
10. Carryover defeats a quick crossover
An invented learning study teaches strategy A in week one and strategy B in week two to the same children. Learning from A may persist during week two. Simply attributing all week-two performance to B confuses order and accumulated learning.
Consider whether the intervention is reversible. If learning persists, a crossover may be unsuitable. Use independent groups, counterbalancing where meaningful or another justified design. A washout label does not make retained knowledge disappear.
11. Missing follow-up behind equal observed percentages
Two invented groups start with 100 participants each. At follow-up, A retains 80 and B retains 95. Sixty-four of A’s 80 observed participants succeed; seventy-six of B’s 95 succeed, both 80% among those measured. Yet attrition is 20% in A and 5% in B.
Equal complete-case percentages do not prove equal outcomes across all initially assigned participants. Investigate missingness and prespecified analysis plans. Make the participant flow visible so readers can judge what the observed denominator excludes.
12. A large sample with very small practical effect
Imagine two conditions have a precisely estimated difference of 0.1 unit on a 100-unit performance scale. With a large sample the statistical test may report a very small p-value, yet the practical importance of that difference still depends on the context, costs, harms and target outcome.
Report the effect, uncertainty, sample design and meaningful decision threshold. A statistically detectable difference is not automatically a useful intervention. Avoid switching from quantitative significance to an unearned claim of major benefit.
13. A sensor swap halfway through the trial
An experiment compares two chemical treatments, but halfway through all measurements switch to a different instrument with a new calibration. If the treatment sequence follows the same time order, the instrument change may masquerade as a treatment effect.
Randomise order where suitable, use common reference samples and document the instrument transition. When a change cannot be avoided, include it explicitly in analysis and interpretation. The design cannot pretend that a major measurement transition did not happen.
14. Changed-context transfer: from independent parts to shared machines
A laboratory factorial design tests independently prepared specimens. The new production version treats several specimens at once in a shared furnace. Their outcomes may now be correlated through batch temperature and equipment conditions; the original assumption of independent specimen treatment no longer holds.
Define the new experimental unit, randomise batches as appropriate and analyse batch effects. Check that factor combinations remain feasible. The best transfer skill is to identify which causal comparison survives when the physical unit of treatment changes.
The connected eduKate research and learning library
Foundations for credible experiments
Scientific measurement and ethical constraints
- Scientific Instrumentation
- Research Ethics
- School Experimental Control Design
- School Scientific Control Group Design
- School Research Data Integrity
Applications in research and teaching
Primary sources for design and bias control
- NIST Engineering Statistics Handbook — Choosing an Experimental Design
- NIST — Blocking Factorial Designs
- NIH Research Methods — Cluster-Randomized Trials
- NIH Research Methods — Choosing the Design
- Cochrane — Risk of Bias in Randomized Trials
- Cochrane — Variants of Randomized Trials
All numerical examples are invented teaching cases, not findings from real schools, workplaces or clinical trials. A real intervention affecting people or regulated materials requires appropriate professional review, permissions, safety procedures and fit-for-purpose statistical planning.
Return to The Gold Standard, Education: Learning Transfers into Life and How X Works.
Worked experimental-design guide: what treatment effect is being estimated
Treatment Fidelity, Protocol Deviations and the Effect Being Estimated — Separate assignment, delivery and receipt before choosing exclusions or naming an effect.
Focused method guide: attrition and missing outcomes
Focused method guide: cluster randomisation
Plan cluster-randomised studies with the correct assignment unit, ICC and effective sample size.
Focused method guide: noncompliance and complier effects
Focused method guide: treatment-effect heterogeneity
Focused method guide: crossover carryover and washout
Focused method guide: factorial estimands and interaction
Adaptive Randomisation, Time Trends and Allocation Bias
How changing allocation probabilities interact with background trends, and how simulations and time-aware analysis protect inference.
NEW SPECIALIST ROUTE
The Gold Standard of Experimental Design | Interim Monitoring, Alpha Spending and Early Stopping
See how planned information times, trial-wide error control and distinct efficacy, futility and safety rules govern early decisions.
NEW SPECIALIST ROUTE
The Gold Standard of Experimental Design | Sham Controls, Blinding Integrity and Expectancy Effects
Define what a sham controls, map role-specific unblinding cues and interpret expectancy evidence without breaking the randomised contrast.
Baseline imbalance, covariate adjustment and chance — a worked guide to the measurement and inference choices behind this experimental design problem.
Randomisation inference, sharp nulls and design-based p values — a worked guide to the measurement and inference choices behind this experimental design problem.
Negative controls, falsification tests and residual bias — a worked guide to the measurement and inference choices behind this experimental design problem.
Interference, spillovers and treatment contamination — Define how treatment reaches connected units, choose the causal contrast and design assignment and inference around exposure.
Multi-arm trials, shared controls and multiplicity — align shared-control efficiency, comparison families and error control.
Missing outcomes, intercurrent events and estimand alignment — align post-randomisation events, outcome collection, estimators and sensitivity analyses with the treatment-effect question.
Composite endpoints, component dominance and interpretability — makes visible which component drives a combined outcome.
Surrogate endpoints, causal mediation and outcome substitution — test whether treatment effects on a proxy support inference about the outcome that actually matters.
Non-inferiority margins, assay sensitivity and constancy — justify acceptable loss, preserve active-control effects and distinguish non-inferiority from an inconclusive comparison.
Stepped-wedge trials, secular trends and time confounding — Separate staggered rollout from causal effect by modelling calendar time, implementation and clustered dependence explicitly.
New specialist route
Regression discontinuity, bandwidth choice and manipulation checks — Earn a local causal claim through a verified cutoff rule, transparent smoothing and sorting diagnostics.
New specialist route
Blinded sample size re-estimation, variance misspecification and Type I error — Repair nuisance-parameter assumptions with a prespecified internal pilot, protected information boundary and verified operating characteristics.
New specialist route
Covariate-adaptive randomisation, minimisation and allocation predictability — Balance prespecified prognostic factors without surrendering allocation concealment, reproducibility or valid inference.
New specialist route
Sequential multiple assignment trials, embedded regimes and dynamic treatment rules — Align sequential randomisations, tailoring variables and shared treatment paths with the adaptive regimes and causal contrasts the trial is designed to estimate.
New specialist route
Micro-Randomised Trials, Proximal Outcomes and Time-Varying Treatment Effects — Use this route to align repeated randomisation with decision points, availability, proximal outcome windows, time-varying effects and treatment burden.
New specialist route
Platform trials, non-concurrent controls and temporal drift extends this subject root with a focused guide to design, evidence, transfer and practical limits.
New specialist route
Basket trials, borrowing across subgroups and exchangeability extends this subject root with a focused guide to design, evidence, transfer and practical limits.
New specialist route
Umbrella Trials, Biomarker Stratification and Shared Screening — Follow the shared screening pathway from biomarker assay to substudy assignment, controls and valid treatment comparisons.
New specialist route
Pragmatic Trials, Treatment Variation and Usual-Care Drift — Test real-world decisions while measuring treatment adaptation, comparator variation, co-interventions and change through calendar time.
New specialist route
Encouragement Designs, Treatment Uptake and Instrument Strength — Separate the randomised offer, treatment uptake and complier effect while testing instrument strength and exclusion assumptions.
New specialist route
Principal stratification — Post-randomisation events, latent strata and estimand interpretation.
New specialist route
Experimental Design: Survivor Average Causal Effects, Truncation by Death and Sensitivity Bounds
New specialist route
Experimental Design: Win Ratios, Generalised Pairwise Comparisons and Clinical Priorities
New specialist route
New specialist route
Continue with The Gold Standard of Experimental Design | Competing Risks, Cause-Specific Hazards and Cumulative Incidence for a worked route from first principles to changed-context transfer, evidence checks and practical limits.
New specialist route
Continue with The Gold Standard of Experimental Design | Multi-State Models, Transition Hazards and State Occupancy for a worked route from first principles to changed-context transfer, evidence checks and practical limits.
New specialist route
Continue with The Gold Standard of Experimental Design | Recurrent Events, Risk Sets and Terminal Events for a worked route from first principles to changed-context transfer, evidence checks and practical limits.
New specialist route
Continue with The Gold Standard of Experimental Design | N-of-1 Trials, Individual Treatment Effects and Repeated Randomisation for a worked route from first principles to changed-context transfer, evidence checks and practical limits.
New specialist route
Continue with The Gold Standard of Experimental Design | Adaptive Enrichment Designs, Biomarker Thresholds and Population Selection for a worked route from first principles to changed-context transfer, evidence checks and practical limits.
New specialist route
Continue with The Gold Standard of Experimental Design | Sample Size Re-Estimation, Information Fractions and Unblinded Variance Reviews for a worked route from first principles to changed-context transfer, evidence checks and practical limits.
New specialist route
Continue with The Gold Standard of Experimental Design | Conditional Power, Predictive Power and Futility Boundaries for a worked route from first principles to changed-context transfer, evidence checks and practical limits.